Study to Assess the Efficacy, Safety, and Tolerability of Vixarelimab in Reducing Pruritus in Prurigo Nodularis: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Study to Assess the Efficacy, Safety, and Tolerability of Vixarelimab in Reducing Pruritus in Prurigo Nodularis (NCT03816891), a randomized phase 2 study. The primary outcome is Phase 2a & 2b: Percent Change From Baseline in Weekly Average Worst Itch-Numeric Rating Scale (WI-NRS) Score.

2. Clinical Question

3. Trial Design

The registry describes a randomized, quadruple-masked, parallel-group Phase 2 study sponsored by Genentech, Inc. The study was marked completed, with enrollment of 240. Its stated focus was the efficacy, safety, tolerability, pharmacokinetics, and immunogenicity of vixarelimab, also identified as KPL-716, in participants with prurigo nodularis. The study title describes it as Phase 2a/b.

The treatment program had two distinct parts. Phase 2a compared weekly subcutaneous vixarelimab with weekly placebo. The active regimen used a 720 mg loading dose followed by 360 mg weekly; the registry describes 8 weeks or 16 weeks of dosing depending on protocol version. Phase 2b used double-blind regimens of vixarelimab 120 mg, 360 mg, or 540 mg every 4 weeks, alongside placebo every 4 weeks. The record also describes a 36-week open-label extension using vixarelimab 360 mg every 2 weeks.

The primary endpoint was measured at different times in the two phases: Week 8 for Phase 2a and Week 16 for Phase 2b. The registry record’s primary analysis population required randomization, at least one dose, and at least one post-baseline efficacy assessment during the double-blind period. It specifies last observation carried forward for Phase 2a and multiple imputation for Phase 2b. Further detail about the imputation procedure is not reported in the registry record.

The original sample-size justification, planned statistical analysis details beyond those stated for the endpoint, and any interim analyses are not reported in the registry record. The total enrollment therefore should not be treated as the number analyzed for every endpoint or treatment comparison.

4. Participant Flow and Accounting

The registry reports how participants moved through each stage of the study. All counts below are exactly as posted; missing counts are not inferred from other stages.

Before assignment: Participants were randomized 1:1 to receive vixarelimab or placebo in Phase 2a. In Phase 2b, participants were randomized 1:1:1:1:1 to receive 4 different dosing regimens of vixarelimab or placebo in a 16-week Double-Blind Period followed by a 36-week Open-Label-Extension (OLE) Period.

Double-Blind Period

Reasons for not completing this period:

Open-Label Period (Phase 2b Only)

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: Modified Intent to Treat (mITT) Analysis Set: All randomized participants who receive at least 1 dose of vixarelimab or placebo and have at least 1 post-baseline efficacy assessment in the double-blind treatment period. Part 2a: Last Observation Carried Forward (LOCF); Part 2b: Multiple imputation (WI)

5. Baseline Characteristics

The table reproduces the baseline characteristics posted in the registry, which describe the participants analysed at baseline and help show whether the randomized groups were comparable.

Population: Modified Intent to Treat (mITT) Analysis Set: All randomized participants who receive at least 1 dose of vixarelimab or placebo and have at least 1 post-baseline efficacy assessment in the double-blind treatment period.

Only the first 6 of 7 groups are shown.

6. Primary Endpoint

The registry lists the primary outcome as Phase 2a & 2b: Percent Change From Baseline in Weekly Average Worst Itch-Numeric Rating Scale (WI-NRS) Score, measured over at Week 8 (Phase 2a); at Week 16 (Phase 2b).

The primary endpoint measures the percentage change from baseline in weekly average WI-NRS score. Participants rated their worst itch daily on a scale from 0, meaning no pruritus, to 10, meaning the worst imaginable pruritus. The endpoint summarizes change in the average of those daily ratings over the specified assessment period.

A percentage change expresses the outcome relative to each participant’s baseline score, rather than only in the original rating-scale units. The registry reports least-squares means and their differences. Least-squares means are model-based group estimates that can account for terms included in the analysis model; the full model specification is not reported in the registry record. The reported dispersion for group means is a standard error, which describes uncertainty in an estimated mean rather than the spread of individual participant scores.

The endpoint is used to compare average changes between randomized groups at a defined follow-up point. Phase 2a assessed it at Week 8, while Phase 2b assessed it at Week 16. That distinction matters: the time points and phase-specific regimens differ, so the results should be interpreted within their respective comparisons rather than as a single common-time-point estimate. The registry states that the least-squares means and differences were rounded to the nearest single decimal place.

7. Results Posted in the Registry

• Phase 2a - Vixarelimab 360 mg SC QW: mean -50.60 versus -29.40 on control; difference -21.20 (95% CI -40.31 to -2.09), standardized effect d = -0.62; z-test p = 0.030.
• Phase 2b - Vixarelimab 540 mg SC Q4W (DBL): mean -56.20 versus -29.40 on control; difference -26.80 (95% CI -43.16 to -10.44), standardized effect d = -0.79; z-test p = 0.001.
• Phase 2b - Vixarelimab 360 mg SC, Q4W (DBL): mean -51.00 versus -29.40 on control; difference -21.60 (95% CI -37.95 to -5.25), standardized effect d = -0.64; z-test p = 0.010.
• Phase 2b - Vixarelimab 120 mg SC, Q4W (DBL): mean -33.00 versus -29.40 on control; difference -3.60 (95% CI -19.98 to 12.78), standardized effect d = -0.11; z-test p = 0.667.

8. Secondary Efficacy Endpoints

The registry also posts results for secondary outcomes. For each outcome below, the endpoint type, the test applied to the posted summary statistics, the result and its interpretation are given in turn. Secondary endpoints are usually not adjusted for multiple testing, so they support rather than confirm the primary finding.

Phase 2a: Percentage of Participants Achieving at Least a 4-point Reduction From Baseline in Weekly Average WI-NRS at Week 8

• Endpoint type: Binary: the percentage of participants with the event (counts rebuilt from the posted percentages and group sizes).
• Test: Unadjusted two-proportion z-test, with a Wald 95% confidence interval for the risk difference.
• Result:
  • Phase 2a - Vixarelimab 360 mg SC QW: 52.2% (12/23) versus 30.8% (8/26) on control; risk difference 21.4 percentage points (95% CI -5.6 to 48.5), risk ratio 1.70 (0.84–3.40); unadjusted two-proportion z-test p = 0.128.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Phase 2a - Vixarelimab 360 mg SC QW and the control. The interval gives the range of effects that remain compatible with the data.

Phase 2a: Percent Change From Baseline in Pruritus Visual Analog Scale (VAS) at Week 8

• Endpoint type: Continuous: a mean value per participant, compared as a difference in means.
• Test: Unadjusted two-sample z-test for the difference in means, using the posted standard errors.
• Result:
  • Phase 2a - Vixarelimab 360 mg SC QW: mean -54.40 versus -32.60 on control; difference -21.80 (95% CI -41.19 to -2.41), standardized effect d = -0.63; z-test p = 0.028.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the mean is statistically lower for Phase 2a - Vixarelimab 360 mg SC QW than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

Phase 2b: Percentage of Participants Achieving at Least a 6-Point Reduction From Baseline in Weekly Average WI-NRS at Week 16

• Endpoint type: Binary: the percentage of participants with the event (counts rebuilt from the posted percentages and group sizes).
• Test: Unadjusted two-proportion z-test, with a Wald 95% confidence interval for the risk difference.
• Result:
  • Phase 2b - Vixarelimab 540 mg SC Q4W (DBL): 42.6% (20/47) versus 2.1% (1/48) on control; risk difference 40.5 percentage points (95% CI 25.8 to 55.2), risk ratio 20.43 (2.86–146.13); unadjusted two-proportion z-test p = <0.001.
  • Phase 2b - Vixarelimab 360 mg SC, Q4W (DBL): 23.4% (11/47) versus 2.1% (1/48) on control; risk difference 21.3 percentage points (95% CI 8.6 to 34.1), risk ratio 11.23 (1.51–83.61); unadjusted two-proportion z-test p = 0.002.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the proportion with the event is statistically higher for Phase 2b - Vixarelimab 540 mg SC Q4W (DBL) than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.
  • The 95% confidence interval excludes no difference, so the proportion with the event is statistically higher for Phase 2b - Vixarelimab 360 mg SC, Q4W (DBL) than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

The secondary outcomes broaden the assessment beyond average percentage change in the primary itch score. They include threshold-based improvements in weekly average WI-NRS, changes in pruritus visual analog scale, and changes in the 5-D Pruritus total score. Across the posted examples, several measures favor active-treatment groups in their point estimates, and the Phase 2b threshold response pattern is generally more pronounced in the higher-dose groups than in the placebo group. The Phase 2a response and visual-analog outcomes also point in the same broad direction as the primary Phase 2a result, although not every secondary comparison has the same strength of evidence.

These outcomes are related to the primary endpoint because they measure itch severity or response, but they do not measure exactly the same quantity. A threshold response counts participants meeting a predefined change criterion, whereas a mean percent change summarizes the group average. A visual analog scale and the 5-D Pruritus score are separate measures. Agreement across related outcomes can add context, but it is not equivalent to independent confirmation.

Secondary results carry less weight when many endpoints or comparisons are examined without a reported multiplicity adjustment. The registry record lists 39 outcome measures and 38 posted secondary measures, but the multiplicity strategy is not reported. When many tests are considered, the chance of at least one nominally notable result can increase. The secondary estimates should therefore be treated as supportive and interpreted with their confidence intervals, sample sizes, prespecification status, and analysis methods in mind. The record does not report enough detail to establish how the full family of secondary tests was controlled.

Secondary outcomes registered for this trial, for reference (only those above were recalculated):

• Phase 2a: Percentage of Participants Achieving at Least a 4-point Reduction From Baseline in Weekly Average WI-NRS at Week 8
• Phase 2a: Percent Change From Baseline in Pruritus Visual Analog Scale (VAS) at Week 8
• Phase 2a: Change From Baseline in Weekly Average of WI-NRS Over Time
• Phase 2a: Percent Change From Baseline in Weekly Average of WI-NRS Over Time
• Phase 2a: Change From Baseline in Pruritis Visual Analog Scale (VAS) Over Time
• Phase 2a: Percent Change From Baseline in Pruritis Visual Analog Scale (VAS) Over Time
• Phase 2a: Change From Baseline in 5-D Pruritus Total Score Over Time
• Phase 2a: Percent Change From Baseline in 5-D Pruritus Total Score Over Time

9. Statistical Interpretation

10. Statistical Methods Explained

What does a least-squares mean represent? A least-squares mean is an estimate of a group’s average outcome from a statistical model. Unlike a raw arithmetic mean, it may account for covariates or other model terms. The registry identifies ANCOVA for the sponsor’s continuous-outcome comparisons, but does not report the complete model specification. The values are therefore best described as model-based estimates, without assuming which adjustments were included.

What does the mean difference express? The mean difference compares the estimated average outcome in one group with that in another. For a percent-change endpoint, a negative difference means the estimated change in the first named treatment group is more negative than the comparator’s estimate, using the comparison’s stated group order. This is a contrast in the endpoint’s units, not a ratio. Its interpretation depends on which comparator was used and which analysis produced the estimate.

What do standard errors and confidence intervals convey? A standard error describes the uncertainty around an estimated mean; it is not the range containing most individual observations. A confidence interval gives a range of values compatible with the data and the analysis procedure at its stated confidence level. A wider interval indicates less precision than a narrower one. Whether an interval includes the null value for a difference is one part of inference, but does not by itself describe clinical importance or rule out bias.

How does ANCOVA differ from a simple recalculation? ANCOVA is a model-based method for comparing outcomes between groups while accounting for specified variables. The sponsor’s reported least-squares mean differences and p-values come from its reported ANCOVA analyses. The recalculated comparisons are simple, unadjusted calculations based on posted summary statistics. They use approximate standard deviations derived from the posted standard errors, rather than participant-level observations or the sponsor’s full model. They cannot reproduce adjustments, missing-data handling, or other model details that are not contained in summary statistics.

Why is the comparator important? Phase 2a and Phase 2b had separate placebo groups. The sponsor-reported Phase 2b analyses compare each Phase 2b dose with the Phase 2b placebo group. The simple recalculations for those arms use the Phase 2a placebo mean as the control, as indicated by the comparison definitions in the record. Those contrasts should not be substituted for the sponsor’s randomized Phase 2b comparisons. The sponsor’s own analysis takes precedence when the two approaches differ.

How are binary outcomes analyzed? A binary endpoint classifies participants according to whether they did or did not meet a stated response threshold. A percentage is the observed proportion meeting that criterion. A risk difference compares the proportions, while an odds ratio compares the odds of the event between groups. These are different effect measures and their numerical values are not interchangeable. The registry reports Cochran-Mantel-Haenszel analyses for the selected binary comparisons. The full details of stratification or adjustment are not reported in the registry record.

What is over-dispersion, in general? In general, over-dispersion occurs when observed variability is greater than a statistical model assumes. It can make uncertainty estimates too small if the model does not account for that extra variation. The registry record does not report an over-dispersion assessment for these outcomes, so no conclusion about whether it occurred can be drawn from the posted summary statistics.

What does a p-value tell the reader? In general, a p-value measures how incompatible the observed data are with a specified null model, under the assumptions of the analysis. It is not the probability that the null hypothesis is true, nor a measure of effect size. The sponsor’s p-values come from its stated analyses; the unadjusted recalculated p-values do not account for multiplicity or reproduce the sponsor’s models. Statistical significance alone does not establish importance, robustness, or relevance to outcomes that were not measured.

How should design and analysis populations be kept distinct? Randomization describes how treatment groups were assigned. The modified intent-to-treat population for the primary endpoint includes only randomized participants who received at least one dose and had at least one post-baseline efficacy assessment during the double-blind period. This is narrower than the concept of analyzing every randomized participant. The record specifies LOCF for Phase 2a and multiple imputation for Phase 2b, but further details of those procedures are not reported.

11. Confidence Intervals and Precision

The sponsor’s Phase 2a primary comparison was a least-squares mean difference of -21.2, with a 95% confidence interval from -40.82 to -1.60. This interval conveys uncertainty around the model-based contrast; it should not be read as a range of individual participant outcomes. Its span also shows that the estimate is not pinned down to a single value. The sponsor reported p = 0.035 for this comparison.

The simple recalculation for Phase 2a gives a difference of -21.2 and an interval from -40.31 to -2.087. It resembles the sponsor’s estimate but differs in interval limits and p-value because it is an unadjusted summary-statistic calculation rather than the sponsor’s ANCOVA. The sponsor’s analysis takes precedence.

For Phase 2b, the sponsor’s estimates are based on comparisons with the Phase 2b placebo group. Their reported confidence intervals are generally informative about uncertainty, but the 360 mg comparison has a reported estimate of -36.4 and limits of -49.6 to 23.3. Those limits are inconsistent with the direction and reported p-value of the estimate, and should not be silently corrected. The record does not resolve the discrepancy.

Confidence intervals for binary endpoints can be particularly wide when event counts are small. In general, a broad interval means that a range of effect sizes remains compatible with the data. The secondary response estimates and intervals should therefore be considered alongside their underlying sample sizes and analysis method, rather than relying on a point estimate alone. Precision is distinct from bias: a narrow interval cannot rule out problems in design, measurement, missing-data handling, or analysis.

12. Planning a Similar Trial: Sample Size

This is a planning illustration, not a re-evaluation of the original trial. It asks: if a new study wanted to detect a difference like the one observed, or a smaller one, how large would it need to be? It is deliberately not “observed power” of the finished trial, which is not a meaningful quantity.

The planning figures are illustrations based on the observed effect, not the trial’s original sample-size justification. They assume a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. The assumed effect to detect is the stated fraction of the observed effect. For continuous outcomes, the figures are participants per arm; for time-to-event outcomes, figures would represent total events. The outcomes represented in these planning comparisons are not time-to-event outcomes, so the displayed planning counts are participants per arm.

The 80% power column gives the illustrative number of participants per arm for a design with an 80% chance of detecting the specified effect under the stated planning assumptions, if that effect and assumptions were correct. The 90% power column gives the corresponding count for a design with a 90% chance. These are prospective planning quantities, not observed properties of the completed study.

Rows for 100%, 75%, and 50% of the observed effect show how the illustrative count changes when the assumed target effect is reduced. Smaller effects need more participants to be detected with the same planned power, all else equal. The figures are sensitive to the estimated effect used as their starting point; an observed effect from a small study can be uncertain and may not recur at the same size.

This is not observed power. The original trial’s own sample-size assumptions and justification are not reported in the registry record. The planning values should therefore be read as conditional illustrations, not as evidence that the trial was adequately or inadequately sized for its original objectives.

13. How the Sample Size Is Derived

Power is the probability that a study of a given size rejects the null hypothesis when a specific true effect exists. It depends on four things: the effect to detect, the variability of the outcome, the significance level (here a two-sided α of 0.05, so z_1−α/2 = 1.960) and the desired power (z_1−β = 0.842 for 80% and 1.282 for 90%).

Formula

n is the number of participants in each arm, Δ is the difference in means to detect and σ is the common standard deviation.

Worked calculation for this trial

1. Observed difference Δ = -21.200; pooled standard deviation σ = 34.140.
2. n = 2 × (1.96 + 0.842)² × 34.140² / -21.200² = 40.7, rounded up to 41 participants per arm for 80% power.

The smaller-effect rows in the table above repeat the same calculation with the effect multiplied by 0.75 and 0.5 (for ratios, applied to the logarithm of the ratio).

R code

alpha <- 0.05
z_a   <- qnorm(1 - alpha / 2)          # two-sided
delta <- -21.2                      # observed difference in means
sigma <- 34.1396414619272                     # pooled standard deviation
n_per_arm <- function(power, frac = 1) {
  ceiling(round(2 * (z_a + qnorm(power))^2 * sigma^2 / (delta * frac)^2, 6))
}
for (f in c(1, 0.75, 0.5))
  cat(sprintf("%3.0f%% of observed effect: n per arm = %s (80%% power), %s (90%% power)\n", 100 * f,
              format(n_per_arm(0.80, f), big.mark = ","), format(n_per_arm(0.90, f), big.mark = ",")))

# Check against R's built-in function (t-based, so very slightly larger)
cat("power.t.test:", round(power.t.test(delta = delta, sd = sigma, power = 0.80)$n, 1), "\n")

# Simulation: exact two-sample t-test using simulated means and variances
set.seed(3816891)
n    <- n_per_arm(0.80)
reps <- 20000
m_diff <- rnorm(reps, delta, sigma * sqrt(2 / n))             # difference in sample means
s2     <- sigma^2 * rchisq(reps, 2 * (n - 1)) / (2 * (n - 1))   # pooled sample variance
tstat  <- m_diff / sqrt(s2 * 2 / n)
cat(sprintf("Simulated power at n = %s per arm: %.3f (%d replicates)\n", format(n, big.mark = ","), mean(abs(tstat) > qt(0.975, 2 * (n - 1))), reps))

Output from running the code

100% of observed effect: n per arm = 41 (80% power), 55 (90% power)
 75% of observed effect: n per arm = 73 (80% power), 97 (90% power)
 50% of observed effect: n per arm = 163 (80% power), 218 (90% power)
power.t.test: 41.7 
Simulated power at n = 41 per arm: 0.789 (20000 replicates)

The simulation draws many sets of group means and variances at the planned sample size and counts how often the two-sample t-test rejects the null. It should land close to the target power; at very small required sample sizes it can fall below it, because the normal approximation is rough there.

14. Analyses Reported by the Sponsor

The sponsor’s reported analyses use ANCOVA for the continuous primary endpoint and provide least-squares mean differences, confidence intervals, and p-values. For Phase 2a, the sponsor’s estimated difference was -21.2, with a 95% confidence interval from -40.82 to -1.60 and p = 0.035. The recalculation from posted summary statistics gives a similar point estimate, but its interval and p-value differ because it is an unadjusted calculation and does not reproduce the sponsor’s model.

For Phase 2b, comparator choice is especially important. The sponsor reports comparisons of each dose with the Phase 2b placebo group. The simple recalculations instead use the Phase 2a placebo mean as the control, so their estimates do not represent the sponsor’s Phase 2b randomized comparisons. They should not be used to replace the sponsor’s estimates.

There is also an inconsistency in the sponsor-reported Phase 2b 360 mg confidence limits: the reported estimate is -36.4, while the limits are -49.6 and 23.3, despite p < 0.001. The registry record does not clarify this. The sponsor’s analysis takes precedence over recalculated summary-statistic results, but the reported inconsistency remains relevant when interpreting the precision of that specific comparison.

15. Multiplicity, Missing Data and Analysis Populations

The primary analysis population is described as modified intent-to-treat: randomized participants who received at least one dose and had at least one post-baseline efficacy assessment during the double-blind period. The record specifies last observation carried forward for Phase 2a and multiple imputation for Phase 2b. It does not report the full imputation model, assumptions about missing data, or sensitivity analyses assessing how conclusions change under alternative missing-data assumptions. The number of participants excluded from each endpoint analysis and the reasons for missing assessments are not reported in the registry record.

The registry lists numerous outcome measures and posted analyses, including 39 outcome measures and 1042 analyses overall. A prespecified multiplicity-control strategy for the primary and secondary comparisons is not reported in the registry record. Without that information, the unadjusted recalculated p-values and nominal secondary p-values should not be interpreted as if they account for all testing. The sponsor’s reported p-values should be understood according to the named analysis, while recognizing that the record does not describe a broader testing hierarchy or correction plan.

The original protocol’s sample-size calculation, assumptions used to select the target effect, and any planned interim analyses are also not reported in the registry record. This means the posted planning illustrations cannot be treated as a reconstruction of the original design rationale. The record gives an analysis population definition and some missing-data procedures, but not enough detail to fully assess selection after randomization, the robustness of imputation, or the consequences of missing outcomes.

In general, missing-data methods and multiplicity decisions influence uncertainty and the interpretation of statistical evidence. These are limitations of the information available in the registry record; they do not by themselves establish that the analyses were inappropriate.

16. Safety Results

The registry reports serious adverse events as affected participants divided by participants at risk.

Deaths

Other (non-serious) adverse events

Participants with at least one non-serious event at or above the registry's 5% reporting threshold.

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: small intestinal obstruction (2.1%), cholelithiasis (2.1%), periorbital cellulitis (2.1%), intervertebral disc protrusion (2.1%), colon cancer (2.1%).

The posted serious adverse event figures are participant counts by treatment group, not rates adjusted for treatment duration or exposure. During the double-blind groups, serious adverse events were reported for 0 of 23 participants in Phase 2a vixarelimab and 0 of 26 in Phase 2a placebo; in Phase 2b, counts were 3 of 47 for 540 mg, 0 of 47 for 360 mg, 1 of 47 for 120 mg, and 3 of 48 for placebo. The open-label extension group reports 8 of 181 participants with a serious adverse event. No deaths were reported in the listed groups.

The record also lists serious-event terms, each with a reported frequency of 2.1%: small intestinal obstruction, cholelithiasis, periorbital cellulitis, intervertebral disc protrusion, colon cancer, and syncope. The registry record does not map each term to a treatment arm or give event timing and exposure details. The open-label extension is not directly comparable with the double-blind groups because it is a different treatment period and group definition. These counts describe what was posted; they do not establish causation or provide a complete safety assessment.

17. What the Result Does, and Does Not, Mean

The results describe group-level changes in a participant-rated itch scale over the time points specified for the two study phases. The sponsor’s analyses report differences between vixarelimab and placebo groups, with the Phase 2a comparison and several Phase 2b comparisons reported as statistically notable by their stated analyses. The estimates and confidence intervals communicate both the direction of the group contrast and uncertainty around its size.

They do not show that every participant experienced the group-average change, nor do they identify which individuals improved or worsened. The WI-NRS is a symptom rating measure, so its results do not by themselves establish effects on every aspect of prurigo nodularis, quality of life, or other outcomes. The registry record’s secondary measures add related symptom information but do not substitute for outcomes that were not measured.

Comparisons across the phases require care. The regimens, time points, and placebo groups differ, and the sponsor’s Phase 2b comparisons use Phase 2b placebo. Simple recalculations that use Phase 2a placebo are not equivalent to those sponsor comparisons. A discrepancy in one reported Phase 2b confidence interval also makes that particular precision estimate difficult to interpret as written.

The posted results do not establish whether differences persist beyond the reported assessment period, whether the same estimates would be seen in other populations, or what the results mean for an individual participant. No treatment recommendation follows from these statistical summaries. The findings should be read as evidence about the registered comparisons and outcomes, with uncertainty, analysis choices, missing-data information, and multiplicity limitations kept in view.

18. Why This Trial Matters Statistically

This study illustrates why a randomized trial’s outcome estimates need to be read together with the analysis that generated them. The sponsor’s least-squares mean comparisons are model-based, while recalculations from group summaries are unadjusted approximations. Similar point estimates can coexist with different confidence limits and p-values because the methods and available information differ.

It also demonstrates how comparator identity affects interpretation. The two study phases each included placebo, but the sponsor’s Phase 2b analyses compare active doses with the Phase 2b placebo group. A recalculation using the Phase 2a placebo mean answers a different question. Naming the groups and phase is essential to understanding the estimand represented by a contrast.

The record further shows why precision and internal consistency matter. Confidence intervals describe uncertainty, but a reported interval that does not align with its point estimate and p-value requires caution rather than silent repair. Secondary outcomes may provide context across related measures, yet numerous analyses make multiplicity and prespecification important. Here, the registry record does not report a multiplicity strategy or the original design assumptions, limiting what can be concluded about the broader testing plan.

Finally, safety counts are descriptive and should not be conflated with a comparative risk assessment, especially when treatment periods differ. Together, these features make the trial a useful example of distinguishing the sponsor’s primary analysis, approximate recalculation, endpoint-specific evidence, and the limits of registry summaries.

19. Limitations

• The posted summary statistics are the only data these results rest on; patient-level data, full protocols and statistical analysis plans are not available.
• Recalculated results are simple, unadjusted calculations from posted summaries. They do not replace the sponsor's prespecified analysis.

The registry record does not provide the full statistical analysis plan, the original sample-size justification, interim-analysis details, or a multiplicity strategy. It also does not report full model specifications for the ANCOVA comparisons, including all adjustment terms. These omissions limit independent assessment of the planned analysis and the relationship between reported estimates and analysis decisions.

The primary analysis population excludes randomized participants without a dose or without a post-baseline efficacy assessment. The record states that LOCF was used in Phase 2a and multiple imputation in Phase 2b, but does not describe the imputation model, assumptions, or sensitivity analyses. Participant flow into each endpoint analysis and reasons for missing outcome data are not reported in the registry record.

The recalculations are based on posted summary statistics, use approximate standard deviations, and are unadjusted. They cannot reproduce participant-level ANCOVA or the sponsor’s handling of missing data. For Phase 2b, the recalculated contrast uses the Phase 2a placebo group, whereas the sponsor’s reported Phase 2b analyses compare with the Phase 2b placebo group. The two estimates therefore answer different comparison questions.

The Phase 2b 360 mg sponsor-reported confidence interval is inconsistent with its estimate and p-value as posted. The record does not explain the discrepancy. Safety counts are not adjusted for exposure, and event-term details by group and timing are not reported in the registry record. The open-label extension figures also represent a different treatment period from the double-blind comparisons.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: Study to Assess the Efficacy, Safety, and Tolerability of Vixarelimab in Reducing Pruritus in Prurigo Nodularis — NCT03816891.
• Registry record last updated 2026-01-13; status last verified 2026-01.
• Results first posted 2026-01-13.
• Data retrieved from ClinicalTrials.gov on 2026-11-09.
• Group sizes, means, event counts and sponsor-reported p-values are reproduced as posted. Effect estimates, confidence intervals and p-values not attributed to the sponsor are independently calculated from the posted summary statistics.

23. Record Summary

NCT03816891 is a completed randomized, quadruple-masked, parallel-group Phase 2a/b study of vixarelimab in participants with prurigo nodularis, with enrollment of 240. The primary outcome was percent change from baseline in weekly average WI-NRS score, assessed at Week 8 in Phase 2a and Week 16 in Phase 2b. Phase 2a studied weekly dosing; Phase 2b studied three every-4-week doses against placebo, with an open-label extension also described.

The sponsor reported ANCOVA comparisons for the continuous primary outcome. The Phase 2a estimate was -21.2, with a 95% confidence interval from -40.82 to -1.60 and p = 0.035. Sponsor-reported Phase 2b comparisons used the Phase 2b placebo group. Recalculated comparisons are unadjusted and, for Phase 2b, use a different placebo comparator. The record has a discrepancy in the 360 mg Phase 2b confidence interval. Missing-data and multiplicity details are incomplete, and safety results are posted as counts by group.